Veterinary · Public health, regulation and professional practice · also EBVM
Designing research, appraising evidence and writing it up: study design, critical appraisal, systematic reviews, research ethics, scientific and grant writing.
In the exams: AVMA COE competency on research; EAEVE Day One competences; ICAR AICE-JRF (research methodology unit)
This subject covers how veterinary knowledge is made and how it is used. It has two halves that need each other. Evidence-based veterinary medicine (EBVM) is the clinician's side: turning an uncertainty about a patient or herd into an answerable question, finding the best evidence, judging whether it is trustworthy and relevant, and applying it with clinical judgement and the owner's values. Research methodology is the producer's side: designing studies that answer questions without bias, doing them ethically, reporting them fully, combining them in systematic reviews, and winning the money to do them.
The manual assumes the statistics taught in Biostatistics, Computer Application & Research Methodology (measures of central tendency and dispersion, probability distributions, tests of significance, sample size). It does not repeat them. It adds the tools specific to evidence-based practice and research synthesis: PICO questions, search strategies, evidence hierarchies and GRADE, risk-of-bias appraisal, the number needed to treat, likelihood ratios, effect sizes, meta-analysis and heterogeneity, reporting guidelines such as CONSORT, STROBE, ARRIVE and PRISMA, research ethics and integrity, scientific writing and grant writing.
Worldwide, this material is examined less as a separate paper than as a competence. The AVMA Council on Education and the EAEVE Day One competences require graduates to use evidence and understand research; licensing vignettes test the interpretation of trial and test results; ICAR's AICE-JRF/SRF and ASRB papers include research methodology; specialist colleges in North America and Europe expect residents to design, publish and appraise research; and postgraduate certificates in advanced practice assess evidence-based practice directly. National rules differ, especially on animal-research law, clinical-trial regulation and funding, and the manual says so where it matters.
Evidence-based medicine was defined by Sackett and colleagues (1996) as the conscientious, explicit and judicious use of current best evidence in making decisions about the care of individual patients. Evidence-based veterinary medicine (EBVM) applies the same idea to animals, and it has always meant the integration of three things: the best available research evidence, the clinician's expertise, and the circumstances and values of the patient and its owner (or, in herd and flock work, the farmer, the business and the regulator). It is not 'cookbook' medicine and it is not the same as 'only randomised trials count'. When good evidence is missing, which in veterinary science is often, EBVM asks the clinician to say so plainly, use the best that exists, and record how the decision was reached.
Veterinary medicine has particular problems. Many species share few trials; much evidence is extrapolated from another species or from laboratory animals; most studies are small, single-centre and funded by a manufacturer; and owners' finances and welfare judgements shape what can be done. The Centre for Evidence-based Veterinary Medicine at the University of Nottingham and RCVS Knowledge in the UK have built resources around these problems, such as BestBETs for Vets (short, structured answers to clinical questions) and the Knowledge Summaries published in the open-access journal Veterinary Evidence. The AVMA Council on Education and the EAEVE Day One competences both expect new graduates to find, appraise and apply evidence, and to take part in research.
EBVM is usually taught as a cycle of five steps, sometimes called the five As. Ask: turn a clinical uncertainty into a focused, answerable question. Acquire: search efficiently for the best evidence that answers it. Appraise: judge the evidence for validity (is it true?), importance (is the effect big enough to matter?) and applicability (does it apply to my patient?). Apply: integrate the evidence with clinical expertise and the owner's values to make a decision. Assess (or audit): evaluate the outcome of the decision and the performance of the process, often through clinical audit, and feed the result back.
Clinical audit is the practice-level counterpart of research. Research asks what the right thing to do is; audit asks whether we are doing it and with what result. A practice might audit its surgical-site infection rate after neutering, compare it with published rates, change its skin-preparation protocol and audit again.
Two kinds of question exist. Background questions ask for general knowledge ('What causes feline hyperthyroidism?') and are answered from textbooks and reviews. Foreground questions ask about a specific decision ('In hyperthyroid cats, does radioiodine give longer survival than medical management?') and need primary research or a systematic review.
A foreground question is built with PICO. P is the patient, population or problem, described with the features that matter (species, age, breed, disease stage, production system). I is the intervention, exposure, test or prognostic factor. C is the comparison, which may be another treatment, a placebo, no treatment or the reference-standard test. O is the outcome, which should be one that matters to the animal or owner (survival, return to function, milk yield, pain) rather than only a surrogate (a laboratory value). Some add T for time frame or S for study type (PICOT, PICOS).
An example: 'In adult dogs with a cranial cruciate ligament rupture (P), does tibial plateau levelling osteotomy (I) compared with lateral fabellotibial suture (C) give better limb function measured by force-plate peak vertical force at six months (O)?'
The type of question determines the ideal design. Therapy or prevention questions are best answered by randomised controlled trials and their systematic reviews. Diagnosis questions need cross-sectional studies that compare the index test with a reference standard in a representative sample. Prognosis questions need cohort studies that follow animals from a common, early point in the disease. Harm and aetiology questions use cohort and case-control studies, because randomising animals to a harmful exposure is usually unethical. For qualitative questions about owners' or farmers' experiences, PICo (population, phenomenon of interest, context) is used instead.
Every study begins with a question that is important, answerable and feasible. The FINER criteria summarise this: Feasible (enough animals, money, time and skill), Interesting, Novel, Ethical and Relevant. A good research question is refined into an objective and, for confirmatory studies, a testable hypothesis stated before the data are collected. The null hypothesis states no difference or no association; the alternative states the effect expected. The primary outcome, the main comparison and the analysis plan should be fixed in a protocol in advance, so that the result cannot be shaped by choices made after seeing the data.
Research can be classified in several ways. Basic research seeks mechanisms; applied and translational research tests whether knowledge works in animals or populations. Exploratory (hypothesis-generating) studies look for patterns; confirmatory (hypothesis-testing) studies test one pre-specified hypothesis. Quantitative research measures and counts; qualitative research uses interviews, focus groups and observation to understand meanings, beliefs and behaviour, for example why farmers do or do not adopt a biosecurity measure. Mixed-methods research combines the two.
In an observational study the investigator does not assign the exposure. Case reports and case series describe one or several animals; they generate hypotheses, document new diseases and adverse reactions, but have no comparison group. A cross-sectional study measures exposure and outcome at one time in a defined population, estimates prevalence and is the usual design for diagnostic-accuracy studies, but cannot show which came first. A case-control study starts from animals with the outcome (cases) and without it (controls) and looks back at past exposures; it suits rare diseases and diseases with long latency, and its measure of association is the odds ratio. Controls must come from the same source population as the cases. A cohort study classifies animals by exposure and follows them forward to measure incidence; it gives risk or rate directly, suits rare exposures and can study several outcomes, but is slow and costly for rare outcomes. A retrospective (historical) cohort uses records collected in the past. Ecological studies compare groups such as countries or herds rather than individuals and risk the ecological fallacy: an association at group level need not hold for individual animals.
In an experimental study the investigator assigns the intervention. In a laboratory or controlled experiment the conditions are tightly controlled, often in research animals. In a clinical trial the animals are patients, often client-owned, in their normal setting; a field trial is the same idea applied to farms or populations. The randomised controlled trial (RCT) is the strongest single design for a question about the effect of an intervention, because random allocation spreads known and unknown confounders evenly between groups on average.
Trial variants include the parallel-group trial (each animal receives one treatment), the crossover trial (each animal receives both treatments in sequence, separated by a washout period; it suits stable chronic conditions and needs fewer animals but fails if the condition changes or the first treatment has carry-over effects), the factorial trial (two or more interventions tested at once, for example a vaccine and a feed additive in a 2 x 2 design), and the cluster-randomised trial (whole pens, herds or practices are randomised, which is natural for herd interventions but needs the analysis to account for clustering). A superiority trial asks whether the new treatment is better; an equivalence trial asks whether two are similar within a pre-set margin; a non-inferiority trial asks whether the new one is not worse than the standard by more than a pre-set margin. Non-blinded, uncontrolled 'before-and-after' studies are weak because of regression to the mean, the natural course of disease and placebo effects by caregivers, which in animals act through the owner's or clinician's assessment.
Every estimate is wrong to some degree. Random error (imprecision) comes from sampling chance; it shrinks as sample size increases and is expressed by the width of a confidence interval. Systematic error (bias) pushes the estimate consistently in one direction and does not shrink with a bigger sample. A large biased study is precisely wrong. Internal validity is the extent to which a study's result is true for the animals studied, free from bias; external validity (generalisability) is the extent to which it applies to other animals, herds or settings. Internal validity comes first: a result that is not true for the study animals cannot be generalised.
Selection bias arises when the animals studied, or the comparison groups, differ systematically from what was intended. Referral-hospital populations differ from first-opinion populations; volunteers' herds differ from the national herd; animals lost to follow-up may differ from those that stay. Information (measurement) bias arises from how data are collected: recall bias in case-control studies when owners of sick animals search their memories harder; observer bias when an assessor who knows the treatment scores lameness more kindly; misclassification of exposure or disease. Confounding occurs when a third factor is associated with the exposure, independently affects the outcome and is not on the causal path between them. Herd size, for instance, can confound an apparent link between a vaccine and lower mortality if larger herds both vaccinate more and have better management.
Randomisation means each animal has a known, usually equal, chance of each treatment, decided by a chance process and not by the clinician. Simple randomisation can leave small trials unbalanced, so block randomisation (balanced allocation within blocks of, say, four or six) and stratified randomisation (separate lists for strata such as breed or parity) are common. Alternation, day of the week, case number or the clinician's judgement are not randomisation and are predictable.
Allocation concealment means that the person enrolling an animal cannot know or influence which group it will join until it is irrevocably enrolled, for example by central randomisation or sequentially numbered, opaque, sealed envelopes. It protects against selection bias and is different from blinding. Blinding (masking) means that owners, caregivers, clinicians, outcome assessors and analysts, as far as possible, do not know the allocation after it is made; it protects against performance and detection bias. Placebos and identical-looking preparations make blinding possible. Where blinding the clinician is impossible, as in comparing two surgeries, the outcome assessor can still be blinded.
Other protections are a pre-specified primary outcome, complete follow-up, and analysis by intention to treat (ITT): every randomised animal is analysed in the group to which it was allocated, whatever happened afterwards. ITT preserves the balance that randomisation created. A per-protocol analysis, restricted to animals that completed treatment as planned, answers a different question and can reintroduce bias, though in non-inferiority trials both analyses are usually reported.
Confounding is controlled at the design stage by randomisation, restriction (studying only one category of the confounder, such as first-lactation cows) and matching (pairing cases and controls on the confounder), and at the analysis stage by stratification (Mantel-Haenszel methods) and multivariable models. Only randomisation deals with confounders nobody has measured. A factor on the causal pathway (an intermediate variable) must not be adjusted for as a confounder, because doing so removes part of the real effect. Causal diagrams (directed acyclic graphs) help researchers decide which variables to adjust for.
Observational associations are judged for causation with the considerations listed by Bradford Hill (1965): strength, consistency, specificity, temporality, biological gradient (dose-response), plausibility, coherence, experiment and analogy. Only temporality, that the cause precedes the effect, is strictly necessary; the others make a causal explanation more or less convincing but none proves it.
Some biases are specific to particular designs. Spectrum bias inflates test accuracy when a diagnostic study enrols only clear-cut cases and healthy controls. Verification (work-up) bias arises when only test-positive animals receive the reference standard. Lead-time bias makes survival seem longer when disease is found earlier by screening without any real benefit. Publication bias, the preferential publication of positive results, distorts whole bodies of evidence and is dealt with in the chapter on systematic reviews.
Searching starts from the type of question. For background knowledge, current textbooks and narrative reviews are efficient. For a foreground question, the searcher looks first for pre-appraised and synthesised evidence (systematic reviews, guidelines, Knowledge Summaries, BestBETs for Vets and other critically appraised topics), then for primary studies.
The main bibliographic databases differ in coverage. MEDLINE, searched free through PubMed, is produced by the US National Library of Medicine and indexes many veterinary journals, but by no means all. CAB Abstracts, produced by CABI, has broad coverage of veterinary, animal-science and agricultural literature, including much from Africa, Asia and Latin America and non-English sources; published comparisons of database coverage of veterinary journals have found it covers more veterinary titles than PubMed. Large multidisciplinary citation indexes such as Web of Science and Scopus allow forward citation searching (who has cited this paper since?). Specialist sources include trial registries, conference proceedings, theses, regulatory documents and the reports of bodies such as WOAH and FAO, which together form the grey literature, material not published through conventional commercial channels. A systematic search uses at least two major databases plus grey literature and hand-searching of reference lists, because no single database is complete.
A search is built from the PICO concepts, usually P and I, sometimes O; comparison and outcome terms are often left out to avoid missing relevant studies. For each concept the searcher lists synonyms, spelling variants (oesophagus and esophagus, haemorrhage and hemorrhage), abbreviations, common and scientific names (cattle, cow, bovine, Bos taurus) and related terms. Within a concept the terms are combined with OR, which broadens the set; the concepts are then combined with AND, which narrows it to records containing all of them. NOT removes records containing a term and should be used sparingly, because it can silently exclude relevant records.
Controlled vocabulary is the database's own index of subject headings, applied by indexers to each record. In MEDLINE these are Medical Subject Headings (MeSH); CAB Abstracts has the CAB Thesaurus. Subject headings catch articles that use different words for the same idea, while free-text (keyword) searching of titles and abstracts catches recent records not yet indexed and terms the vocabulary lacks. A good search uses both. Truncation (an asterisk after a word stem, so that 'vaccin*' finds vaccine, vaccines, vaccination), phrase searching with quotation marks, field tags (title, abstract, author) and proximity operators refine the search. Syntax differs between database interfaces, so a strategy must be translated, not copied, from one database to the next.
Search sensitivity (recall) is the proportion of all relevant records that the search retrieves; precision is the proportion of retrieved records that are relevant. The two pull against each other. A clinician wanting a quick answer accepts low sensitivity for high precision; a systematic reviewer accepts very low precision, often only a few per cent of retrieved records being relevant, to reach high sensitivity. Validated search filters (hedges) exist for study types such as randomised trials, and for animal studies in some databases.
A systematic search is planned in a protocol, ideally designed with or checked by an information specialist (the PRESS checklist is used for peer review of electronic search strategies), and reported fully: the databases and interfaces, the date of each search, the complete strategy for at least one database, any limits (language, date) and how grey literature was sought. Limiting to English risks language bias, which matters in veterinary science where much relevant work is published in Chinese, Portuguese, Spanish, French and other languages. Search results are exported to reference-management software, duplicates removed, and records screened against pre-specified eligibility criteria.
Study designs differ in how well they protect against bias for a given type of question, which is the basis of evidence hierarchies, often drawn as a pyramid. For questions about the effect of an intervention, a common ordering from strongest to weakest is: systematic reviews and meta-analyses of well-conducted randomised controlled trials; individual randomised controlled trials; non-randomised controlled studies and cohort studies; case-control studies; cross-sectional studies; case series and case reports; and expert opinion, narrative review, and laboratory or in-vitro work extrapolated to the clinical question. Many veterinary versions place studies in the target species above those in other species, and clinical studies above experimental-infection models.
The Oxford Centre for Evidence-Based Medicine (OCEBM) Levels of Evidence (2011 version) refined this by giving a separate ladder for each type of question: treatment benefits, harms, diagnosis, prognosis, prevalence and screening. For diagnosis, for instance, the top level is a systematic review of cross-sectional studies with consistently applied reference standard and blinding, not a review of trials. The OCEBM table allows a study to be moved down a level for poor quality, imprecision, indirectness or inconsistency, or up for a very large effect.
The pyramid is a rule of thumb, not a law. A badly conducted trial can be less trustworthy than a careful cohort study; a meta-analysis of small, biased trials can be precisely wrong; and some questions, such as rare adverse effects or long-term harms, are better answered by large observational studies.
The GRADE approach (Grading of Recommendations Assessment, Development and Evaluation) rates the certainty of a body of evidence for each important outcome, not single studies. Certainty is graded as high, moderate, low or very low. Evidence from randomised trials starts as high; evidence from observational studies starts as low. Five domains can lower certainty: risk of bias, inconsistency (unexplained heterogeneity between studies), indirectness (the population, intervention, comparison or outcome differs from the question, which is common when evidence comes from another species), imprecision (wide confidence intervals or few events) and publication bias. Three factors can raise certainty for observational evidence: a large magnitude of effect, a dose-response gradient, and a situation in which all plausible residual confounding would reduce the observed effect.
GRADE then separates the certainty of evidence from the strength of a recommendation, which is strong or weak (conditional). A recommendation also weighs benefits against harms, values and preferences, costs and feasibility, so a strong recommendation can rest on low-certainty evidence when the balance is clear, and a weak one on high-certainty evidence when benefits and harms are finely balanced.
Herd-health, food-safety and public-health questions bring extra considerations. The unit of interest may be the herd rather than the animal; outcomes include production, economic returns and public-health risk; and the strongest feasible design may be a cluster-randomised field trial or a well-designed observational study. Risk assessment, as used by WOAH and Codex for trade and food safety, combines evidence from many sources, including expert elicitation, in a structured way. Expert opinion has its place when other evidence is lacking, but it should be gathered systematically, for example by a Delphi process with anonymous rounds and controlled feedback, rather than by asking the most senior person in the room.
Clinical practice guidelines from professional bodies translate evidence into recommendations; their quality can be judged with the AGREE II instrument, which looks at scope, stakeholder involvement, rigour of development, clarity, applicability and editorial independence. A guideline is only as good as the evidence and process behind it, and should state how strong each recommendation is and on what certainty of evidence it rests.
Critical appraisal asks three things of any study. Are the results valid, that is, was the study designed and run so that its results are likely to be true? What are the results, and how large and how precise is the effect? Are the results applicable to my patient, herd or setting? Appraisal checklists exist for each design (for example those of the Critical Appraisal Skills Programme and the Joanna Briggs Institute), and reporting guidelines such as CONSORT tell the reader what a trial report should contain, but the three questions underlie all of them.
For a trial, validity questions include: Was allocation truly random and was it concealed? Were the groups similar at baseline? Were owners, clinicians and outcome assessors blinded? Were the groups treated equally apart from the intervention? Was follow-up complete, and were all animals analysed in the groups to which they were randomised? Was the primary outcome pre-specified, ideally in a registered protocol, and is it the one reported? The Cochrane Risk of Bias tool version 2 (RoB 2) organises these concerns into five domains: bias arising from the randomisation process, bias due to deviations from intended interventions, bias due to missing outcome data, bias in measurement of the outcome, and bias in selection of the reported result. For controlled studies in laboratory animals, the SYRCLE risk-of-bias tool adapts the Cochrane approach.
A baseline table showing similar groups is reassuring but cannot prove randomisation; significance tests of baseline differences in a properly randomised trial are not meaningful, because any difference is by definition due to chance.
For a yes/no outcome, let the control event rate (CER) be the proportion with the outcome in the control group and the experimental event rate (EER) the proportion in the treated group. The relative risk (risk ratio) is EER / CER. The absolute risk reduction (ARR) is CER - EER. The relative risk reduction (RRR) is ARR / CER, equal to 1 - RR. The number needed to treat (NNT) is 1 / ARR, rounded up to the next whole animal: the number of animals that must be treated for one extra animal to benefit compared with the control. For a harmful outcome the same calculation gives the number needed to harm (NNH).
Worked example: in a trial of a prophylactic treatment against neonatal calf diarrhoea, 30% of control calves and 18% of treated calves develop diarrhoea. RR = 0.18 / 0.30 = 0.60. RRR = 40%. ARR = 0.30 - 0.18 = 0.12. NNT = 1 / 0.12 = 8.3, rounded up to 9 calves. The same RRR of 40% applied to a herd where only 5% of calves would otherwise be affected gives ARR = 0.02 and NNT = 50. Relative measures are fairly stable across baseline risks; absolute measures, which matter for decisions and costs, depend on the baseline risk of the patient or herd. Reports that give only relative reductions make treatments look more impressive than they may be for a low-risk animal.
For continuous outcomes the effect is a difference in means with its confidence interval. Precision is judged from the 95% confidence interval: a narrow interval that excludes no effect and includes only clinically important effects is convincing; a wide one that spans both trivial and large effects means the trial was too small to answer the question. Statistical significance is not clinical importance; the minimal clinically important difference should be stated in advance.
Applicability asks whether the study animals resemble my patient (species, breed, age, disease severity, concurrent disease), whether the intervention is feasible here (drug available and legal for this species, skill and equipment present), whether all important outcomes were measured, including harms and costs, and whether the benefit outweighs harm, cost and inconvenience given this owner's values. For food animals, withdrawal periods, legal restrictions on drug use and the economics of treatment are part of the decision.
Common traps in reading trials include: surrogate outcomes presented as if they were patient outcomes; composite outcomes in which a trivial component drives the result; subgroup claims from many unplanned comparisons; trials stopped early for benefit, which overestimate effects; and abstracts and conclusions that are more positive than the results (spin). Industry funding is not by itself proof of bias, but it should prompt a careful look at the comparator chosen, the outcomes selected and whether negative results are reported. For livestock and food-safety trials the REFLECT statement adapts CONSORT to issues such as herd-level allocation and natural disease challenge.
A diagnostic-accuracy study compares an index test with a reference standard in animals suspected of having the condition. Validity questions are: Was there an independent, blinded comparison with an appropriate reference standard? Did the sample include the spectrum of animals in whom the test will be used in practice (mild and early cases, and animals with diseases that mimic the target), rather than obvious cases and healthy controls? Did all animals receive the reference standard, whatever the index-test result? Were the test methods described well enough to repeat? QUADAS-2 is the standard tool for risk of bias in diagnostic-accuracy studies, with domains for patient selection, index test, reference standard, and flow and timing. STARD 2015 (30 items) sets out what such a study should report.
Results are given as sensitivity and specificity, from which likelihood ratios are derived. The positive likelihood ratio LR+ = sensitivity / (1 - specificity); the negative likelihood ratio LR- = (1 - sensitivity) / specificity. They convert a pre-test probability into a post-test probability through odds: pre-test odds = p / (1 - p); post-test odds = pre-test odds x LR; post-test probability = odds / (1 + odds). Worked example: a test with sensitivity 90% and specificity 80% has LR+ = 0.9 / 0.2 = 4.5 and LR- = 0.1 / 0.8 = 0.125. In a dog with a pre-test probability of 20% (odds 0.25), a positive result gives post-test odds 1.125 and probability 53%; a negative result gives odds 0.031 and probability 3%. As a rough guide, LRs above 10 or below 0.1 change probability a great deal; those between 0.5 and 2 hardly change it. Unlike predictive values, likelihood ratios do not depend on prevalence, which is why they transfer better from a study to a clinic.
For prognosis, the key questions are whether the cohort was assembled at a common, early point in the disease (an inception cohort), whether follow-up was long and complete enough, whether outcomes were defined objectively and assessed blind to prognostic factors, and whether a separate validation group confirmed any prognostic model. Results are expressed as survival proportions at set times, median survival with confidence intervals, and hazard ratios. Referral populations usually have worse prognoses than first-opinion ones.
For harm and aetiology studies, the questions are whether the compared groups were similar in all important ways other than the exposure, whether exposure and outcome were measured the same way in both groups, whether follow-up was long and complete, whether confounders were measured and adjusted for, and whether the Bradford Hill considerations support causation. The Newcastle-Ottawa Scale is one tool for appraising cohort and case-control studies, rating selection, comparability and outcome or exposure. STROBE (22 items) sets the reporting standard for observational studies, and STROBE-Vet (2016) extends it to veterinary issues such as clustering of animals within herds and the description of the source population of animals and owners.
Systematic reviews themselves are appraised: was the question focused, the search comprehensive, study selection and data extraction done in duplicate, risk of bias assessed, and pooling appropriate? AMSTAR 2 is a widely used tool for this.
A critically appraised topic (CAT) is a short, structured summary of the best evidence on one clinical question. It contains a clinical scenario, the PICO question, the search strategy and date, the studies found and selected, a summary and appraisal of each, and a 'clinical bottom line', the conclusion a busy clinician can apply, with a statement of its certainty. BestBETs for Vets and the RCVS Knowledge Summaries are published examples of this format, and many veterinary schools set CATs as assessed coursework.
The strengths of a CAT are speed, transparency and teaching value. Its weaknesses are that it usually relies on a limited search, is often written by one person, and goes out of date as new studies appear, so it should carry the search date and an expiry or review date. A CAT that finds no good evidence is still useful: it records that the question has been asked, shows where research is needed and protects against overconfident claims.
A narrative review summarises literature chosen by the author; a systematic review answers a focused question using explicit, reproducible methods to find, select, appraise and synthesise all relevant studies. Its steps are: frame the question (PICO) and eligibility criteria; write and register or publish a protocol in advance; search comprehensively; screen titles and abstracts, then full texts, against the criteria, usually by two reviewers independently with disagreements resolved by discussion or a third reviewer; extract data in duplicate on a piloted form; assess risk of bias in each study; synthesise the results, statistically where appropriate (meta-analysis) and otherwise narratively; rate the certainty of the evidence (for example with GRADE); and report transparently.
PRISMA 2020 (Preferred Reporting Items for Systematic reviews and Meta-Analyses) is the reporting guideline, with a 27-item checklist and a flow diagram showing the number of records identified, duplicates removed, records screened and excluded, full texts assessed and excluded with reasons, and studies included. Extensions cover protocols (PRISMA-P) and scoping reviews (PRISMA-ScR). A scoping review maps the extent and nature of the literature on a broad topic and usually does not appraise or pool; a rapid review shortens some steps for urgent decisions and must say which. In veterinary and animal-health science, systematic reviews of laboratory-animal studies (supported by groups such as SYRCLE and CAMARADES) and of livestock interventions are growing, and the Cochrane Handbook remains the main methods reference.
Agreement between screeners is often summarised with Cohen's kappa, which corrects observed agreement for agreement expected by chance.
Meta-analysis combines the effect estimates of several studies into a weighted average. For binary outcomes the effect is usually a risk ratio or odds ratio, analysed on the log scale; for continuous outcomes it is a mean difference (same scale in all studies) or a standardised mean difference (different scales), such as Cohen's d = (mean1 - mean2) / pooled SD, or Hedges' g, which multiplies d by a small-sample correction J = 1 - 3 / (4(n1 + n2 - 2) - 1).
In the inverse-variance method each study's weight is 1 / variance of its effect, so large, precise studies count most. Worked example with three trials of a calf-diarrhoea prophylaxis, deaths treated versus control: trial 1, 6/50 vs 12/50 (RR 0.50); trial 2, 10/80 vs 14/80 (RR 0.71); trial 3, 3/40 vs 12/40 (RR 0.25). The variance of ln RR is 1/a - 1/n1 + 1/c - 1/n2, giving 0.210, 0.146 and 0.367, so weights of 4.76, 6.83 and 2.73. The fixed-effect pooled ln RR is the weighted mean, -0.655, giving a pooled RR of 0.52 (95% CI 0.31 to 0.87), from SE = 1 / square root of the sum of weights.
A fixed-effect (common-effect) model assumes one true effect shared by all studies; a random-effects model assumes the true effects vary between studies around a mean and adds a between-study variance, tau-squared, to each study's variance, commonly estimated by the DerSimonian-Laird method. Random-effects models give relatively more weight to small studies and wider confidence intervals when heterogeneity exists. In the example tau-squared is 0.018 and the random-effects RR is 0.51 (0.30 to 0.88), almost identical because heterogeneity is low.
Heterogeneity is variation in results beyond chance. Cochran's Q is the weighted sum of squared deviations of each study's effect from the pooled effect, compared with a chi-square distribution on k - 1 degrees of freedom; it has low power when there are few studies. I-squared = (Q - df) / Q, set to zero when Q is smaller than df, expresses the percentage of variation due to heterogeneity rather than chance. In the example Q = 2.16 on 2 df, so I-squared is 7%. Higgins and colleagues suggested 25%, 50% and 75% as low, moderate and high; the Cochrane Handbook instead gives overlapping bands (0-40% might not be important, 30-60% moderate, 50-90% substantial, 75-100% considerable). Heterogeneity is explored by pre-specified subgroup analysis or meta-regression, never by quietly dropping awkward studies. A forest plot shows each study's estimate and confidence interval, its weight (box size) and the pooled estimate (diamond), against a line of no effect.
Publication bias occurs because studies with positive or significant results are more likely to be published, published quickly and published in English. A funnel plot of effect size against precision should look like an inverted, symmetrical funnel; asymmetry with small negative studies missing suggests small-study effects, of which publication bias is one cause among others (poor quality of small studies, true heterogeneity). Egger's regression test assesses asymmetry formally but needs about ten or more studies; trim-and-fill imputes apparently missing studies as a sensitivity analysis. The remedies are to search grey literature and trial registries and to register trials prospectively. A meta-analysis is only as good as the studies in it: pooling biased studies gives a precise, biased answer.
Research on animals is regulated by law in most countries, and the details differ. In the European Union, Directive 2010/63/EU governs animals used for scientific purposes, requires project authorisation with a harm-benefit analysis and classifies procedures by severity. In the UK, the Animals (Scientific Procedures) Act 1986 requires licences, and each establishment has an Animal Welfare and Ethical Review Body (AWERB). In the USA, the Animal Welfare Act and the Public Health Service Policy require review by an Institutional Animal Care and Use Committee (IACUC). In India, the Committee for Control and Supervision of Experiments on Animals (CCSEA, formerly CPCSEA) registers establishments, which run Institutional Animal Ethics Committees (IAECs). Researchers must check their own national law and institution's rules.
The common principle is the 3Rs of Russell and Burch (1959): Replacement (avoid or replace animal use, for example with in-vitro, computer or human-volunteer methods), Reduction (use the minimum number of animals that will answer the question, through good design and statistics) and Refinement (minimise pain, suffering and distress and improve welfare, through anaesthesia, analgesia, housing, handling and humane endpoints). An underpowered study wastes animals as surely as an oversized one, because it cannot answer its question. Humane endpoints are pre-defined criteria at which an animal is removed from a study or euthanased to prevent further suffering.
Clinical research on client-owned animals raises its own issues. Owners must give informed consent, understanding the purpose, the procedures, the risks and benefits, the costs, what happens to data and samples, and their right to withdraw without affecting their animal's care. Whether a clinical study needs ethical review depends on national rules and on whether the procedures go beyond normal veterinary practice; good practice, and most journals, now expect ethical review of clinical studies. In the UK, the RCVS provides an ethics review panel for practitioners without access to an institutional committee. For trials supporting the registration of veterinary medicines, VICH guideline GL9 sets Good Clinical Practice.
Research misconduct is usually defined, as in US federal policy, as fabrication (making up data or results), falsification (manipulating materials, equipment or processes, or changing or omitting data, so that the record is inaccurate) or plagiarism (using another's ideas, words or results without credit), in proposing, performing, reviewing or reporting research. Honest error and differences of opinion are not misconduct. Self-plagiarism, such as duplicate publication of the same results, and image manipulation are also integrity breaches.
Beyond outright misconduct lie questionable research practices: selective reporting of outcomes, p-hacking (trying analyses until one reaches significance), HARKing (Hypothesising After the Results are Known), dropping inconvenient data points without a pre-specified rule, and salami-slicing one study into many minimal papers. These distort the literature more widely than fabrication. Remedies include pre-registration of protocols and analysis plans, registered reports (peer review of the protocol before results exist), sharing data and code, and reporting all outcomes.
Data should be managed so that they are accurate, secure and, where possible, findable, accessible, interoperable and reusable (the FAIR principles). Personal data about owners and clients must be handled under the data-protection law of the country. Conflicts of interest, financial or personal, must be declared in protocols, papers and peer reviews. The Committee on Publication Ethics (COPE) publishes guidance and flowcharts that journals follow when misconduct is suspected; corrections and retractions repair the record.
The International Committee of Medical Journal Editors (ICMJE) recommends that authorship be based on all four of these criteria: substantial contributions to the conception or design of the work, or the acquisition, analysis or interpretation of data; drafting the work or revising it critically for important intellectual content; final approval of the version to be published; and agreement to be accountable for all aspects of the work. Many veterinary journals use these criteria. Acquiring funding, supervising a group or collecting data alone does not justify authorship; such contributors are acknowledged. Gift (honorary) authorship gives credit to someone who did not meet the criteria; ghost authorship hides someone who wrote the paper, often a commercial medical writer.
Author order conventions vary by field and country; the first author usually did most of the work, and the last author is often the senior supervisor. The CRediT (Contributor Roles Taxonomy) system lists 14 roles, such as conceptualisation, methodology, formal analysis and writing, so that each author's actual contribution is stated. Persistent identifiers, such as the ORCID identifier for researchers and the DOI for papers and datasets, help credit reach the right people.
Most research papers follow the IMRaD structure: Introduction (why the study was done), Methods (how), Results (what was found) and Discussion (what it means). The title should be specific and informative, often naming the species, design and main finding. The abstract, frequently structured under the same headings and limited to about 250 words depending on the journal, is all that most readers will see and must report the main numerical result with its confidence interval, not just a P value.
The introduction moves from the general problem to the specific gap and ends with the aim or hypothesis. The methods must be detailed enough for another researcher to repeat the study: design, setting, animals and eligibility, ethical approval, interventions, outcomes and how they were measured, sample-size reasoning, randomisation and blinding, and statistical methods. Results present the flow of animals, baseline characteristics, then outcomes, in text, tables and figures without repeating the same numbers in all three, and without interpretation. The discussion opens with the main finding, compares it with other work, explains strengths and limitations honestly, and states conclusions that the data support, avoiding 'spin'.
Good scientific prose is plain and precise: short sentences, the active voice where it helps, consistent terms, defined abbreviations, and numbers with units and appropriate precision. Reference styles are either numbered (Vancouver) or author-date (Harvard); the journal's instructions decide. Reference-management software reduces errors, but every cited source must be read and must actually support the claim.
Reporting guidelines list the minimum information a reader needs to judge and repeat a study. They are collected by the EQUATOR Network. The main ones for veterinary research are: CONSORT for randomised trials (the 2010 statement, a 25-item checklist with a participant flow diagram, was updated in 2025); REFLECT, an extension for randomised trials in livestock and food safety; STROBE for observational studies (22 items) and STROBE-Vet for veterinary observational studies; STARD 2015 for diagnostic-accuracy studies (30 items); PRISMA 2020 for systematic reviews (27 items); ARRIVE for animal research; CARE for case reports; and SPIRIT for trial protocols.
The ARRIVE guidelines (Animal Research: Reporting of In Vivo Experiments) were revised as ARRIVE 2.0 in 2020. They are organised into the ARRIVE Essential 10, the minimum without which a reader cannot judge reliability (study design, sample size, inclusion and exclusion criteria, randomisation, blinding, outcome measures, statistical methods, experimental animals, experimental procedures and results), and the Recommended Set of 11 further items that give context (such as the abstract, background, objectives, ethical statement, housing and husbandry, animal care and monitoring, interpretation, generalisability, protocol registration, data access and declaration of interests). Many journals require a completed checklist on submission.
Reporting guidelines are not quality scores: a well-reported study can still be badly designed. They are best used at the planning stage, so that the study collects what will need to be reported.
Peer review is the evaluation of a manuscript by experts before publication. In single-blind review the reviewers know the authors' identities but not the reverse; in double-blind review neither knows; in open review identities, and sometimes reports, are published. The editor decides: accept, minor or major revision, or reject. Authors respond to reviewers point by point, saying what was changed and where, and politely explaining any disagreement with evidence. A rejection is common and not final; most papers are published, often in another journal after improvement.
Choosing a journal involves its scope and readership, indexing in the main databases, peer-review practice, speed, open-access options and costs. Open access may be gold (the final version free at the publisher, often paid by an article-processing charge), green (an accepted manuscript deposited in a repository) or diamond (free to read and to publish). Preprints share a manuscript publicly before peer review. Predatory journals charge fees while offering little or no genuine peer review or editorial service; warning signs include unsolicited flattering emails, very fast acceptance, hidden fees, fake indexing claims and an editorial board that cannot be verified. Checking a journal's membership of recognised bodies such as COPE or listing in the Directory of Open Access Journals helps.
Metrics are used, and misused, to judge journals and researchers. The journal impact factor for a year is the number of citations received in that year by items the journal published in the two previous years, divided by the number of citable items it published in those two years. A researcher's h-index is the largest number h such that h of their papers have each been cited at least h times. Both depend on field and career stage; the San Francisco Declaration on Research Assessment (DORA) urges assessing research on its own merits rather than by journal metrics.
Research money comes from national research councils and government agencies, international bodies, charities and foundations, industry, and institutions' own funds. Examples include ICAR and the Department of Biotechnology in India, the Biotechnology and Biological Sciences Research Council in the UK, the National Institutes of Health and the USDA National Institute of Food and Agriculture in the USA, and the European Union's Horizon Europe framework programme; many animal-health charities fund clinical veterinary research. Each funder has a mission, eligibility rules, budget limits, deadlines and assessment criteria, and the first task is to read the call and guidance closely and, where possible, talk to the programme officer.
Reviewers and panels judge proposals on a broadly similar set of questions, though each funder words them differently: Is the problem important? Is the idea new? Are the aims clear and the methods sound and feasible? Is the team able to do it, with the right skills and environment? Is the budget justified and good value? Will the results have impact, scientific and beyond? Is the work ethical, with animal use justified under the 3Rs?
A typical proposal contains a title; a summary, often both technical and lay; aims and objectives; background and rationale with the knowledge gap; preliminary data showing feasibility; the research plan; a timeline; a budget and its justification; the team; expected outputs and impact; ethics and animal-welfare statements; a data management plan; and references. The aims page is the most important: it states the problem, the gap, the overall goal or central hypothesis, two to four specific aims, and the expected result. Objectives should be SMART: specific, measurable, achievable, relevant and time-bound.
The research plan explains for each aim the design, animals or samples, sample size with its justification, measurements, analysis, expected results, potential problems and alternative strategies. Larger projects are organised into work packages with milestones (points of progress) and deliverables (tangible outputs), shown on a Gantt chart. A risk register lists what could go wrong (a disease outbreak on the study farm, a delay in ethical approval, a key person leaving) with its likelihood, impact and mitigation. A logic model or theory of change links inputs and activities to outputs, outcomes and impact, and is increasingly expected for applied and development projects.
The budget lists direct costs: staff, consumables, animals and their care, equipment, travel, field costs, publication and dissemination. Indirect costs (overheads) cover the institution's estates, administration and services; funders handle them differently, as a percentage of direct costs, a percentage of total costs, a fixed rate, or not at all. UK research councils, for instance, generally fund a set percentage of the full economic cost. Each item must be justified: why this many samples, this much staff time, this equipment.
Strong proposals are written early, reviewed internally by colleagues who were not involved, and rewritten. They use the funder's headings and language, put the key message at the start of each section, avoid unexplained jargon and use figures to show the design. Common reasons for rejection are an unfocused or overambitious plan, aims that depend on each other so that failure of one sinks all, lack of preliminary data, weak statistical design, an unclear gap, and a mismatch with the funder's remit. Many funders allow resubmission; a resubmission answers the previous reviews explicitly.
Once funded, the project is managed against its plan. The principal investigator is responsible for the science, the budget, staff, compliance with ethics and animal licences, data management and reporting to the funder. Changes in aims or budget usually need the funder's permission. Interim and final reports are compared with the milestones and deliverables promised. Results should be published whether positive or negative, data deposited as the data management plan promised, and findings communicated to farmers, practitioners, owners and policy-makers in forms they can use.
A student uses this subject to stop memorising lists and start asking where a statement comes from. Practical tasks: write a PICO question from a case seen on rotation, search CAB Abstracts and PubMed with Boolean operators and subject headings, appraise one trial and one diagnostic study, and write a critically appraised topic with an honest clinical bottom line. For the final-year project, the student writes a short protocol with an aim, design, sample-size reasoning and ethics approval, follows the relevant reporting guideline, and learns that a negative result honestly reported is still a result.
Five years into practice, the vet uses EBVM when an owner brings an internet claim, when a sales representative presents a new product, and when the practice reviews its protocols. Tasks: convert relative risk reductions in promotional material into absolute risks and NNTs for the practice's own patients; use likelihood ratios to decide whether a test result changes management; run a clinical audit of, say, post-operative infections or antimicrobial use and act on it; take part in a multi-centre clinical trial, obtaining owner consent and collecting data to protocol; and write a case report following the CARE guideline.
A senior practitioner or head of a herd-health, government or industry team decides policy for many animals. They commission or write practice guidelines and judge them with GRADE and AGREE II; decide whether evidence is strong enough to change a vaccination, treatment or control programme; supervise residents' and interns' research; review manuscripts for journals; sit on ethics committees, weighing harm against benefit and the 3Rs; and recognise when industry-funded evidence omits comparators or outcomes. They also mentor juniors in authorship ethics and protect them in integrity disputes.
A researcher with a PhD and long experience designs programmes, not single studies. They write competitive grant applications with clear specific aims, work packages, risk registers and justified budgets; design cluster-randomised field trials and non-inferiority trials with pre-registered protocols; lead systematic reviews and meta-analyses with PRISMA reporting and GRADE certainty ratings; handle heterogeneity and publication bias properly; manage data to FAIR principles; and serve on funding panels and editorial boards. They also shape research culture, through registered reports, data sharing and fair assessment of researchers beyond journal metrics.
This manual does not teach the statistics of hypothesis tests, sample-size formulas or regression; those are in Biostatistics, Computer Application & Research Methodology. Qualitative research methods are introduced only briefly. Meta-analysis is taught to the level of inverse-variance pooling, DerSimonian-Laird random effects, I-squared and funnel plots; network meta-analysis, diagnostic-test meta-analysis (bivariate models) and individual-participant-data meta-analysis are named but not taught. Country-specific animal-research and clinical-trial law is summarised for the EU, UK, USA and India only; readers elsewhere must check national rules. Item counts are given only for reporting guidelines whose counts are well established; the CONSORT 2025 update is mentioned without detail. Named funders are examples, and their rules, overhead rates and review criteria change often and must be checked in the current call.
Original practice questions written to the syllabus and pattern of the exams named in each question's examTags. They are not past papers and do not reproduce any board's questions.
These notes are free to read here, with no account.
What the Laisha app adds:
Free for ten days, then a subscription. We would rather write that here than have you find it later.